Molecular profiling reveals features of clinical immunity and immunosuppression in asymptomatic P. falciparum malaria

Abstract Clinical immunity to P. falciparum malaria is non‐sterilizing, with adults often experiencing asymptomatic infection. Historically, asymptomatic malaria has been viewed as beneficial and required to help maintain clinical immunity. Emerging views suggest that these infections are detrimental and constitute a parasite reservoir that perpetuates transmission. To define the impact of asymptomatic malaria, we pursued a systems approach integrating antibody responses, mass cytometry, and transcriptional profiling of individuals experiencing symptomatic and asymptomatic P. falciparum infection. Defined populations of classical and atypical memory B cells and a TH2 cell bias were associated with reduced risk of clinical malaria. Despite these protective responses, asymptomatic malaria featured an immunosuppressive transcriptional signature with upregulation of pathways involved in the inhibition of T‐cell function, and CTLA‐4 as a predicted regulator in these processes. As proof of concept, we demonstrated a role for CTLA‐4 in the development of asymptomatic parasitemia in infection models. The results suggest that asymptomatic malaria is not innocuous and might not support the induction of immune processes to fully control parasitemia or efficiently respond to malaria vaccines.

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Studniberg et al. used a combination of systems biology tools and analysis to characterize differences among healthy individuals, symptomatic malaria, and asymptomatic malaria and found several parameters that correlate with disease severity. In addition, they discovered an immunosuppressive transcriptional signature with upregulation of pathways involved in the inhibition of T cell function, and CTLA-4. They then further validated this finding in mouse model of malaria. This is a welldesigned and executed study and the manuscript is well written as well. I only have some minor questions and suggestions. 1. For Figure 1G, they need to include or discuss the Pf antibody titer in normal healthy individuals, not living in those endemic area. 2. Their PD-1 cytof signal is low. Therefore, I think it is necessary to show that the antibody itself is working. 3. Figure 3B missing label for significance. 4. I think it would be interesting to discuss a literature survey on whether people with asymptomatic malaria would have a poor response rate to regular vaccines given that they have a immunosuppressive signature.

Reviewer #2:
This is an interesting paper that contains a goldmine of data and hints at some novel inflammatory, metabolic and immune pathways associated with malaria infection. However, in its current format it presents a somewhat confusing, and at times contradictory, story. However, with a major rewrite, and perhaps a reframing of the underlying hypotheses, it could make a valuable contribution to the literature. Firstly, the title is somewhat misleading and fails to capture the full extent of the observations presented. One aspect of the data (relating to AM) seems to have been plucked out of the many observations and highlighted, over emphasising one aspect of the data at the expense of the rest. The focus, in the introduction and discussion, is on the potential deleterious consequences of asymptomatic malaria infections. The appropriate comparator group for such analysis is with the healthy controls, as any intervention would aim to convert these people to a healthy state, however in many of the analyses the primary comparisons are between AM and SM or between SM and HC, with much less attention paid to the AM/HC comparison. Indeed, the comparison of RNAseq data between AM and HC is only presented in the supplementary figures, not in the main text. I would argue that there are three valid comparisons to be made in this analysis: AM vs HC, AM vs SM and SM vs HC. All three should be shown wherever possible. Comparison of AM with HC is essential to determine whether AM is deleterious. Throughout the paper, the authors refer to pathways that down regulate T cell effector functions as "immunosuppressive". Another way to think of it is that these responses are "immunoregulatory" and thus supportive of homeostasis, rather than "immunosuppressive" which implies that they are in some way pathological. The authors have not really presented any data to demonstrate that down regulation of the T cell response is detrimental. On a related point, there is some rather simplistic thinking . For example, the implication that upregulation of inflammatory pathways that mediate disease symptoms will automatically lead to inhibition of acquisition of antibody-mediated immunity. This assumes that the concentrations of cytokines mediating inflammation are the same as those that modulate antibody responses. This is not necessarily the case and it is at least plausible that one outcome can occur independently of the other depending on the timing, concentration and wider environment of the response. This cross-sectional study design does not allow causality to be ascribed to any of the observations and certainly does not allow the direction of any supposed causal relationship to be determined. In order to begin to demonstrate causality, and to predict which parameter predicts which, you need a longitudinal study design and/or corroboration of the observational data with experimental data. The corroboration of the CTLA-4 data in the mouse model is a very nice example of this, but it is the only example. The manuscript is littered with comments suggesting causality and the direction of causality, e.g : Page 8, line 7: "PD-1 +CXCR3+ T-bet+ TFH cells predicted increased susceptibility to P. falciparum symptomatic malaria P8 line 9: "classical and activated MBCs were associated with increased risk of symptomatic infection Page 8 Line 13 "associated with protection from symptomatic infection .....Thus, diverse MBCs expressing low chemokine receptors levels and a CD4+ TH2 cell bias predict reduced risk of clinical malaria. Page 12. Line 8 "downregulated by asymptomatic malaria" P12, Line 21 "indicate that low parasitemia asymptomatic P. falciparum infections activate a blood transcriptional profile that drives several immunosuppressive processes" (This could be rephrased as a hypothesis rather than stated as a fact ). Page 19 line 12 and 14; upregulated by asymptomatic infection"; "asymptomatic malaria induced the upregulation of NR1D1 " There are many more. The entire ms. needs to be carefully checked and these statements of association or prediction removed or qualified.
I have some concerns over the study design that limit the utility of the data. No consideration is given to these limitations in either the presentation or interpretation of the data. For example, • this is an opportunistic study based on stored samples that were not collected with this purpose in mind. To what extent has this hampered the execution of the study? Were there limitations in cell numbers, cell quality (the cells have been stored for more than a decade, how were they quality controlled?), RNA quality etc that have limited the number of assays performed.
• only a subset of samples were analysed by RNA seq. How were these samples selected? On the basis of sample quality? If so, how comparable are the groups included in the RNA seq analysis (data for the full cohort is shown in Fig 1; we need to see the same data just for the subset included in the RNA seq analysis).
• whilst the groups are roughly comparable, overall, the age range is very broad. Have you checked to see whether there are any age effects on any of the analyses? • similarly, the range of parasitemias is quite high (and overlapping) between AM and SM. Have the data been checked for any association with parasitemia? Fig 3 (and elsewhere) -why are all 3 groups not shown side by side on the same bar charts? Difference between AM and HC is as important as differences between AM vs SM. Throughout the manuscript, differences are reported as being statistically significant but the statistical data are not provided. Stats should be given (in the text or figures) for all differences that are claimed to be significant, and should be adjusted for age and parasitemia if necessary. Finally, the authors present some interesting and plausible hypotheses relating to upregulation and down regulation of different pathways. It would be really helpful -and would greatly increase the accessibility of the findings -if these ideas could be summarised in a graphical summary or graphical abstract.

Reviewer #3:
Studniberg and colleagues investigate immune phenotypes of healthy uninfected individuals, and P. falciparum infected individuals with and without malaria symptoms by mass cytometry and RNAseq and antibody responses, and search for associations. While the work is well done a presented I provide a few ideas, that I believe will help improve the manuscript.
The authors often refer to cell populations predicting increased or decreased susceptibility to P. falciparum symptomatic malaria, but their data is associative only. Individuals showing symptoms or not at the time of cell collection only, without any longitudinal data. Although interesting, i believe the wording should be revised. For instance MBCs expressing low chemokine receptors were more commonly seed in individuals without clinical malaria, but they might not be predictive of protection, and only be more expressed once symptoms arise. How was the number samples used for PBMC RNAseq decided and how were these selected from the larger pool? this should be clear in the methods or result section. How did the 5 or 6 samples included compare to the rest in terms of parasitemia and T and B cell subpopulations. In my view the authors should be caustics as to define direction and causation of the association seen in these data.
I recommend altering the title of section "Asymptomatic P. falciparum malaria supports humoral responses to infection while driving cell mediated immunosuppressive responses" and very little if anything on the data shown refers, in my view, to humoral responses.
It is possible that an antibody-dependent immune response controls parasite numbers and as such less immune cell effector function is promoted, and not only activation of immunosuppressive signatures The mouse data show low parasitamieas following an acute infection while the AM human data is likely the product of infection continuously remaining below the clinical threshold. I recommend infection mice with much lower number of iRBCs to better mimic an asymptomatic infection, or to be more cautious regarding its interpretation. the authors do a good job in referring to work showing expression data of previous studies, and this reviewer agrees that there is a lack in RNAseq data of AM, but the reference cited Boldt et al PMID: 30638864 includes asymptomatic infection and could be mentioned and maybe mentioning immune phenotypic done through other techniques as done by Andrade et al. PMID: 33106664 could be worth discussing.
Minor commnents There is a new who malaria report from 2021, shall the authors want to refer top the latest numbers Portugal et al, 2017 shows only that treating children right before the season starts has no effect on clinical malaria risk, but it remains unclear if immunomodulatory effects would require more time to fade away after clearance, and this could be more clearly transmitted Please indicate whether mean and SD, median and IQR, or whatever it is shown in figure legends.
Indicate also what the dashed line on Fig 1G shows and how background was controlled for in the legend or methods section.
If there are significant differences in Fig. 3 these should be identified in the Figure. In the section "Asymptomatic P. falciparum malaria drives a transcriptional profile supporting immunosuppressive processes" it seems that Fig 6C is  We sincerely thank the reviewers for taking the time to assess our manuscript. We found the feedback very useful in improving to the delivery of our study. We welcome the suggestion to elaborate more on the genes differentially expressed between asymptomatic individuals and healthy controls, which has now allowed us to bring to the surface important information hidden in the analysis.

Studniberg et al. used a combination of systems biology tools and analysis to characterize differences among healthy individuals, symptomatic malaria, and asymptomatic malaria and found several parameters that correlate with disease severity. In addition, they discovered an immunosuppressive transcriptional signature with upregulation of pathways involved in the inhibition of T cell function, and CTLA-4. They then further validated this finding in mouse model of malaria. This is a well-designed and executed study and the manuscript is well written as well. I only have some minor questions and suggestions.
We thank the reviewer por the positive appraisal of our manuscript.

For Figure 1G, they need to include or discuss the Pf antibody titer in normal healthy individuals, not living in those endemic area.
Thanks, for the comment. Antibody levels of malaria-naïve healthy Melbourne controls were shown as a dotted line in Fig 1G. This has now been clarified in the figure legend.

Their PD-1 cytof signal is low. Therefore, I think it is necessary to show that the antibody itself is working.
Although the PD-1 CyTOF signal is low compared to other markers in the panel, the metallabelled antibody used in our stainings produces highly reproducible results. Similar populations of CD27 + PD-1 + T H1 -like memory CD4 + T cells and CXCR3 + T-bet + PD-1 + memory T FH cells have been detected in the present manuscript as wells as in P. vivaxinfected individuals in a recently published study (JCI Insight 2021;6(14):e148086). We have confirmed the expression of PD-1 in these cells by manual gating. An example showing percentage of PD-1 + cells among gated CD3 + cells (top) and PD-1 expression among gated CD4 + T H1 cells (bottom) is provided in the reviewer's figure.

Figure 3B missing label for significance.
The results in Figs 3A-E were generated using the CITRUS algorithm in Cytobank. CITRUS is an algorithm designed for the fully automated discovery of statistically significant stratifying biological signatures within single cell datasets containing numerous samples across multiple known endpoints. CITRUS performs unsupervised hierarchical clustering to identify clusters of cellular populations within the overall dataset. CITRUS then uses a regularized supervised learning algorithm to determine the populations and features that best predict differences across groups. A false discovery rate (FDR) is set up before the algorithm starts to run the analysis. Our analysis was performed at an FDR of 5% (p<0.05). More information has been provided both in the Results section and figure legend to be better explain how CITRUS discovers significantly different populations across groups.

I think it would be interesting to discuss a literature survey on whether people with asymptomatic malaria would have a poor response rate to regular vaccines given that they have a immunosuppressive signature.
Thank you for this excellent suggestion. We have included in the discussion examples of attenuated sporozoite immunisation results, showing that vaccine immunogenicity is significantly reduced in malaria-exposed African adults compare to malaria-naïve controls. a somewhat confusing, and at times  contradictory, story. However, with a major rewrite, and perhaps a reframing of the  underlying hypotheses, it could make a valuable contribution to the literature. Thank you for acknowledging the potential of our study. We have taken the reviewer's comments onboard, and we trust that this revised version provides a more balanced delivery of our findings.

Firstly, the title is somewhat misleading and fails to capture the full extent of the observations presented. One aspect of the data (relating to AM) seems to have been plucked out of the many observations and highlighted, over emphasising one aspect of the data at the expense of the rest.
We agree with the reviewer. Our proposed title was longer and had to be shortened to meet editorial requirements. In this revised version, we have changed it to "Molecular profiling reveals an immunosuppressive signature in asymptomatic P. falciparum malaria", which is under 100 words. We will be happy to change the tittle to "Molecular profiling reveals features of clinical immunity and immunosuppression in asymptomatic P. falciparum malaria", that better captures all responses found in the study, provided editorial approval.

The focus, in the introduction and discussion, is on the potential deleterious consequences of asymptomatic malaria infections. The appropriate comparator group for such analysis is with the healthy controls, as any intervention would aim to convert these people to a healthy state, however in many of the analyses the primary comparisons are between AM and SM or between SM and HC, with much less attention paid to the AM/HC comparison. Indeed, the comparison of RNAseq data between AM and HC is only presented in the supplementary figures, not in the main text. I would argue that there are three valid comparisons to be made in this analysis: AM vs HC, AM vs SM and SM vs HC. All three should be shown wherever possible. Comparison of AM with HC is essential to determine whether AM is deleterious.
The reviewer raised an important point. We have now moved the contrast between AM vs HC out of EV and into a new primary figure (Figure 7). We elaborated a lot more on various immunoregulatory pathway impacted by asymptomatic infection. Furthermore, we have included examples of specific immunoregulatory genes which are equally upregulated or downregulated by asymptomatic malaria compared to both symptomatic individuals and healthy controls ( Figure 7E).

Throughout the paper, the authors refer to pathways that down regulate T cell effector functions as "immunosuppressive". Another way to think of it is that these responses are "immunoregulatory"
and thus supportive of homeostasis, rather than "immunosuppressive" which implies that they are in some way pathological. The authors have not really presented any data to demonstrate that down regulation of the T cell response is detrimental.
Thanks for the comment. To further the analysis around this topic we have now looked at correlations of immunoregulatory genes differentially expressed between asymptomatic vs symptomatic individuals and parasitemia. We have found two groups of genes, some that show significant correlations with parasitemia and some that did not. We hypothesized that changes in transcriptional profiles of immunoregulatory genes as a function of high parasitemia could be driven by high parasite burdens and/or the concomitant inflammation associated with symptomatic infection, and presumably respond to homeostatic requirements. In contrast, we suggest that changes in transcriptional profiles not correlated with high parasitemia, might result from persistent clinicallysilent infections. These concepts are now included in the manuscript.
Old Figure 8 (now Figure 9) provides proof of concept for the T cell suppressive-CTLA-4 pathway in the control of asymptomatic parasitemia. Furthermore, we also show identified similar sources of CTLA-4 expression during asymptomatic infection in rodent and P. falciparum human malaria. It is possible that immunosuppressive processes arise as a homeostatic mechanism to prevent inflammation-driven pathology during persistent asymptomatic infection, but at the expense of reducing the capacity of the cellular response to fully control parasitemia. This concept has been added to the discussion.

On a related point, there is some rather simplistic thinking . For example, the implication that upregulation of inflammatory pathways that mediate disease symptoms will automatically lead to inhibition of acquisition of antibody-mediated immunity. This assumes that the concentrations of cytokines mediating inflammation are the same as those that modulate antibody responses. This is not necessarily the case and it is at least plausible that one outcome can occur independently of the other depending on the timing, concentration and wider environment of the response.
Thank you for pointing this out. The concept that IFN-gamma-mediated responses modulate the acquisition of humoral immunity arises from a large body of data in humans and mice demonstrating an important upregulation of the T H1 -defining transcription factor T-bet in T FH cells, which results in diminished helper capacity. We fully agree with the reviewer that the role of inflammatory pathway in the control of humoral response is complex than that our data shows that too. For example, we found that T-bet plays a dual role in infection. While Tbet expression in T FH cells impairs their differentiation, thereby reducing the magnitude of the antibody response, T-bet expression in B cells promotes the differentiation of cells with increased affinity for antigen, thereby improving the quality of the antibody response. This has now been incorporated into the Introduction.

The manuscript is littered with comments suggesting causality and the direction of causality, e.g : Page 8, line 7: "PD-1 +CXCR3+ T-bet+ TFH cells predicted increased susceptibility to P. falciparum symptomatic malaria P8 line 9: "classical and activated MBCs were associated with increased risk of symptomatic infection Page 8 Line 13 "associated with protection from symptomatic infection .....Thus, diverse MBCs expressing low chemokine receptors levels and a CD4+ TH2 cell bias predict reduced risk of clinical malaria. Page 12. Line 8 "downregulated by asymptomatic malaria"
We acknowledge the limitations of a not longitudinal follow up. We have extensively revised the manuscript and endeavoured to find a more balance wording to describe the results. In some experiments, we performed logistic regression and obtained statistically significant odds ratios. By definition, odds ratios give information on the probability or risk of an event occurring or not, even in not longitudinal settings. We have rephrased as required to make sure that our wording reflects that.

P12, Line 21 "indicate that low parasitemia asymptomatic P. falciparum infections activate a blood transcriptional profile that drives several immunosuppressive processes" (This could be rephrased as a hypothesis rather than stated as a fact ).
This sentence has been largely rephrased in the context of our new correlation analysis of transcriptional profiles with parasitemia levels. In brief, we now say …" raising the possibility that low parasitemia asymptomatic P. falciparum infections activate a blood transcriptional profile that drives immunosuppressive processes"…

Page 19 line 12 and 14; upregulated by asymptomatic infection"; "asymptomatic malaria induced the upregulation of NR1D1 " There are many more. The entire ms. needs to be carefully checked and these statements of association or prediction removed or qualified.
The manuscript was thoroughly checked and rephrased to achieve a more balanced delivery of our findings.

I have some concerns over the study design that limit the utility of the data. No consideration is given to these limitations in either the presentation or interpretation of the data. For example, • this is an opportunistic study based on stored samples that were not collected with this purpose in mind. To what extent has this hampered the execution of the study? Were there limitations in cell numbers, cell quality (the cells have been stored for more than a decade, how were they quality controlled?), RNA quality etc that have limited the number of assays performed.
The study was specifically set up in the Timika region for the purpose of the current study: identify parameters associated with clinical immunity to malaria We have recently published the P. vivax arm of this study in a recent paper (Ioannidis et al, JCI insight, 2021). Samples were collected by Indonesian staff in Timika, who prepared plasma and PBMC that were rapidly frozen and stored in liquid nitrogen. Cell and RNA quality was good. Strict ethics protocol in Indonesia allowed collection of no more than ~ 5-10 ml of blood from consenting participants. On occasions, no enough material was obtained to run all endpoints proposed in the study, which explains the smaller subset employed for RNA-sequencing. Fig 1;

we need to see the same data just for the subset included in the RNA seq analysis).
Samples were selected for RNA-seq on the basis on material abundance. Samples with larger cell number, with enough material to run CyTOF and RNA-seq were used for this analysis. Clinical parameters (parasitemia, hematocrit, etc), a range of antibody responses and cell populations identified by CyTOF of the subgroup used for RNA-seq were representative of values observed across the larger cohort. We have created a new figure ( Figure EV2) showing that there were no significant differences across these endpoints between the average of the full cohort and the sub-group used for transcriptomics analysis.

• whilst the groups are roughly comparable, overall, the age range is very broad. Have you checked to see whether there are any age effects on any of the analyses?
Age was not found to be a confounder in this cohort. Papuans reside both in the Timika lowlands where malaria exposure is common and the highlands where malaria is absent. Migration of non-immune adults from the highlands to lowlands means a first malaria infection (often symptomatic) can occur in all age groups. This is a highly unique scenario, compared to many settings in Africa, in which younger people develop symptomatic infection and adults are asymptomatic carriers, and age is clearly a confounder. This information has been added to the study design.

• similarly, the range of parasitemias is quite high (and overlapping) between AM and SM. Have the data been checked for any association with parasitemia?
Parasitemia was not a confounder in the cohort. By study design, symptomatic individuals are by definition higher in parasitemia than asymptomatic ones. As stated in the methods all individuals included in the analysis of immune response had >500 parasite/mL blood.
As discussed above, we have looked at specific correlations of selected immunoregulatory genes differentially expressed between AM vs SM and parasitemia and found that whereas most transcriptional profiles are not correlated with parasitemia, a few genes showed negatively associated with high parasitemia. The implication of the findings is discussed in manuscript, as mentioned above.

Fig 3 (and elsewhere) -why are all 3 groups not shown side by side on the same bar charts? Difference between AM and HC is as important as differences between AM vs SM.
The results in Figs 3A-E were generated using the CITRUS algorithm in Cytobank. CITRUS is an algorithm designed for the fully automated discovery of statistically significant stratifying biological signatures within single cell datasets containing numerous samples across multiple known endpoints. CITRUS performs unsupervised hierarchical clustering to identify clusters of cellular populations within the overall dataset. CITRUS then uses a regularized supervised learning algorithm to determine the populations and features that best predict differences across groups. That is why some populations were identified as differentially abundant between HC and SM and not necessarily between AM and SM and vice verse. A false discovery rate (FDR) is set up before the algorithm starts to run the analysis. Our analysis was performed at 5%FDR (p<0.05). More information has been provided both in the Results section and figure legend to be better explain how CITRUS discovers significantly different populations across groups.

Throughout the manuscript, differences are reported as being statistically significant but the statistical data are not provided. Stats should be given (in the text or figures) for all differences that are claimed to be significant, and should be adjusted for age and parasitemia if necessary.
No confounders were identified in the cohort. We have corrected all stats missing throughout the figure legends.

Finally, the authors present some interesting and plausible hypotheses relating to upregulation and down regulation of different pathways. It would be really helpful -and would greatly increase the accessibility of the findings -if these ideas could be summarised in a graphical summary or graphical abstract.
Excellent suggestion. The revised version includes a synopsis image.

Studniberg and colleagues investigate immune phenotypes of healthy uninfected individuals, and P. falciparum infected individuals with and without malaria symptoms by mass cytometry and RNAseq and antibody responses, and search for associations. While the work is well done a presented I provide a few ideas, that I believe will help improve the manuscript.
We thank the reviewer for the positive appraisal of our manuscript.

The authors often refer to cell populations predicting increased or decreased susceptibility to P. falciparum symptomatic malaria, but their data is associative only. Individuals showing symptoms or not at the time of cell collection only, without any longitudinal data. Although interesting, i believe the wording should be revised. For instance MBCs expressing low chemokine receptors were more commonly seed in individuals without clinical malaria, but they might not be predictive of protection, and only be more expressed once symptoms arise.
Thank you for the fair suggestion. We acknowledge the limitations of a not longitudinal follow up. We have extensively revised the manuscript and endeavoured to find a more balance wording to describe the results. In some experiments, we performed logistic regression and obtained statistically significant odds ratios. By definition, odds ratios give information on the probability or risk of an event occurring or not, even in not longitudinal settings. We have rephrased as required to make sure that our wording reflects that.

I believe comparisons shown in Fig 3 would gain from showing all 3 population and not only two, it is not clear why some show HC and SM, while other show AM and SM.
The results in Figs 3A-E were generated using the CITRUS algorithm in Cytobank. CITRUS is an algorithm designed for the fully automated discovery of statistically significant stratifying biological signatures within single cell datasets containing numerous samples across multiple known endpoints. CITRUS performs unsupervised hierarchical clustering to identify clusters of cellular populations within the overall dataset. CITRUS then uses a regularized supervised learning algorithm to determine the populations and features that best predict differences across groups. That is why some populations were identified as differentially abundant between HC and SM and not necessarily between AM and SM. A false discovery rate (FDR) is set up before the algorithm starts to run the analysis. Our analysis was performed at a 5%FDR (p<0.05). More information has been provided both in the Results section and figure legend to be better explain how CITRUS discovers significantly different populations across groups.

How was the number samples used for PBMC RNAseq decided and how were these selected from the larger pool? this should be clear in the methods or result section.
Samples were selected for RNA-seq on the basis on material abundance. Samples with larger cell number, with enough material to run CyTOF and RNA-seq (as well as other endpoints not shown in the manuscript) were used for this analysis. Our preliminary experiments indicated that ~6 samples/group were enough to provide good segregation of transcriptional profiles at a 15%FDR. This information has been included in the text.

How did the 5 or 6 samples included compare to the rest in terms of parasitemia and T and B cell subpopulations. Fig 3 could easily show the proportions of the different CD4 and MBC subpopulations and then identify the 5 or 6 samples use din Fig 4.
Clinical parameters (parasitemia, hematocrit, etc), a range of antibody responses and cell populations identified by CyTOF of the subgroup used for RNA-seq were representative of values observed across the larger cohort. We have created a new figure ( Figure EV2) showing that there were no significant differences across these endpoints between the average of the full cohort and the sub-group used for transcriptomics analysis.

this would also allow better discussing if RNAseq differences observed in Fig 4are likely to be promoted by different proportions of cell types, and support or not the statement "suggesting that transcriptional differences detected downstream would reflect changes in cell activity between clinical groups rather than fluctuations in the composition of the PBMC pool." which reads too strong to me without more data rot back it. Furthermore, up-regulation of terms involved in cell proliferation in symptomatic malaria by the RNAseq data might point to increase of particular subpopulations
Thanks for pointing this out. That is correct. New Figure 8 (old Fig 7) shows a correlation between terms involved in proliferation and IgM + activated MBC, abundant among symptomatic individuals. The d-tangle package only infers broad populations (like total MBC, CD4 + , CD8 + T cells) and fluctuations in smaller subsets cannot be detected. The statement has been deleted. Fig 4C. That was a mistake and we thank the reviewer for pointing this out. We have corrected Fig  4D using (Idaghdour et al, 2012;Lee et al, 2018;Tran et al, 2016)that detection of blood transcriptional activity in response to infection, diminishes with lower parasitemia levels. Thus, a 15%FDR was used to improve detection of transcribed genes during low parasitemia asymptomatic infection.

The authors could try to identity the cell populations/pathways promoting the gene expression differences between AM and SM, but should be cautious and have into account if gene expression differences between AM and HC are present (as in cluster 4 of Fig 6c, otherwise differences between AM and SM might be just a product of differences between symptoms or not. Accordingly, in my view some of Fig EV2 should be made available in the main manuscript figures. In my view the authors should be caustics as to define direction and causation of the association seen in these data.
The reviewer raised an important point. We have now moved the contrast between AM vs HC out of EV and into a new primary figure (Figure 7). We elaborated a lot more on various immunoregulatory pathway impacted by asymptomatic infection. Furthermore, we have included examples of specific immunoregulatory genes which are equally upregulated or downregulated by asymptomatic malaria compared to both symptomatic individuals and healthy controls ( Figure 7E).
In Figure 6, we have now looked at correlations of immunoregulatory genes differentially expressed between asymptomatic vs symptomatic individuals and parasitemia. We have found two groups of genes, some that show significant correlations with parasitemia and some that did not. We hypothesized that changes in transcriptional profiles of immunoregulatory genes as a function of parasitemia could be driven by high parasite burdens and/or the concomitant inflammation associated with symptomatic infection. In contrast, we propose that changes in transcriptional profiles not correlated with high parasitemia, are more likely to be the result of persistent clinically-silent infections. These concepts are now included in the manuscript.

I recommend altering the title of section "Asymptomatic P. falciparum malaria supports humoral responses to infection while driving cell mediated immunosuppressive responses" and very little if anything on the data shown refers, in my view, to humoral responses.
The title was changed to "Asymptomatic P. falciparum malaria-immunosuppressive transcriptional profiles are not correlated responses associated with reduced risk of symptomatic infection"

It is possible that an antibody-dependent immune response controls parasite numbers and as such less immune cell effector function is promoted, and not only activation of immunosuppressive signatures
Yes. We agree. It is possible that there is no need to mount a high cellular response when there are high antibody levels. However, asymptomatic infections are persistent and difficult to self-resolve, even with good antibody levels, suggesting an additional role for T cell responses in immunity. Our analysis uncovered several anti-proliferative and antiinflammatory pathways upregulated during these infections and using a mouse infection model we provided proof of concept that blockade of one of these pathways (CTLA-4) facilitates the control of asymptomatic parasitemia. It is therefore possible that immunosuppressive mechanisms arise to prevent inflammation-driven pathology during persistent infections but at the expense of reducing the capacity of the cellular response to fully control parasitemia. We have added this concept to the discussion.

The mouse data show low parasitamieas following an acute infection while the AM human data is likely the product of infection continuously remaining below the clinical threshold. I recommend infection mice with much lower number of iRBCs to better mimic an asymptomatic infection, or to be more cautious regarding its interpretation.
The infection model does not shield reproducible results using infections with much lower number of iRBCs. We have rephrased the text to acknowledge the limitations of the mouse infection model and the differences with human malaria.

the authors do a good job in referring to work showing expression data of previous studies, and this reviewer agrees that there is a lack in RNAseq data of AM, but the reference cited Boldt et al PMID: 30638864 includes asymptomatic infection and could be mentioned and maybe mentioning immune phenotypic done through other techniques as done by Andrade et al. PMID: 33106664 could be worth discussing.
Thanks for the suggestion. The two references have been added to the discussion.

Minor commnents There is a new who malaria report from 2021, shall the authors want to refer top the latest numbers
The 2021 WHO malaria report in now quoted.

Portugal et al, 2017 shows only that treating children right before the season starts has no effect on clinical malaria risk, but it remains unclear if immunomodulatory effects would require more time to fade away after clearance, and this could be more clearly transmitted
The text in the introduction and discussion has been modified.

Please indicate whether mean and SD, median and IQR, or whatever it is shown in figure legends.
We have including all missing statistical parameters from the figure legends. Thank you.

Indicate also what the dashed line on Fig 1G shows and how background was controlled for in the legend or methods section.
Antibody levels of malaria-naïve healthy Melbourne controls were shown as a dotted line in Fig 1G. This has now been clarified in the figure legend.
If there are significant differences in Fig. 3 these should be identified in the Figure. As discussed above, CITRUS is an algorithm designed for the fully automated discovery of statistically significant signatures within single cell datasets. A false discovery rate is set up before the algorithm starts to run the analysis. Our analysis was performed at a 5%FDR (p>0.05). This is the p value for all identified populations. This has been clarified in the text.

In the section "Asymptomatic P. falciparum malaria drives a transcriptional profile supporting immunosuppressive processes" it seems that Fig 6C is wrongly called 5C, please correct.
Thank you. This has been corrected.

Legend of Figures with Chord diagrams should be more complete and better guide the reader to what connection are highlighted in the text and what are represent different colours on the inner circle.
We have included extra labelling in the chord diagrams for clarity. As we now elaborated more on the genes differentially expressed between asymptomatic infection and controls, relevant genes from that group have been incorporated into the chord too (New Figure 8D).

Point-by-Point to the editors queries MSB-2021-10824R Initial Quality Check
We would like to thank the editors very much for the outstanding quality check of our manuscript. Please find our point-by-point response to the editor queries below: * Pre-acceptance checks by our data editors have raised a few queries in the manuscript which you will find as comments in the attached edited/commented Word document with "Track changes" activated. We would appreciate if you incorporated the requested final text modifications directly into this attached version, uploading the edited document upon resubmission with changes/additions still highlighted via the "Track changes" option. This will help us to facilitate our final checking.
We have addressed all comments within the attached manuscript and have highlighted all changes via the track changes option. The finalised manuscript has been re-uploaded to the portal.
* Dataset GSE181179 is not accessible/available, please provide access for referees/editor. Please also remember that all datasets must be publicly accessible latest upon acceptance.
Dataset GSE181179 has now been made publicly accessible.
* Figure 4. The legend describes A-D but the figure displays A-E. Figure 4E is also not listed in the figure legend or called out in the manuscript.
This was our mistake as we had uploaded an old version of figure 4. The new version that does not include a figure 4E has been re-uploaded.
* During a standard image analysis we detected potential duplications in the figure set, 2 A-E and 3 A-E. We would like you to clarify this issue before sending your paper back to referees. Please update the respective figure legends or if you make changes to the figures, please include a point-by-point describing what you have changed.
We have repeated t-SNE panels in figures 2A-E and in figures 3A-E intentionally to facilitate interpretation of figure 3. However, we will be happy to remove the repeated t-SNE panels in figures 3A-E if the editors consider them to be redundant. Thank you for sending us your revised manuscript. We have now heard back from reviewer #3 who was asked to evaluate your revised study. As you will see below, they think that the reviewers' concerns have been satisfactorily addressed. I am glad to inform you that we can soon accept the study for publication, pending some minor editorial issues listed below, as well as a minor issue listed by the reviewer.
-Please make all requested text changes using the attached .doc file and *keeping the "track changes" mode* so that we can easily access the edits made.
-There is a callout to Supplementary -Our data integrity analyst noted that Figure panels 2A-E are reused in Figure 3A-E. We would ask you to clearly indicate the data/panel reuse in the respective figure legends for transparency.
-We agree with using the title "Molecular profiling reveals features of clinical immunity and immunosuppression in asymptomatic P. falciparum malaria", you can update the text accordingly.
-The provided synopsis image is rather detailed and does not display well at the required final size (i.e. 500 px width). Please provide an updated image, exactly at this size (width = 500 px, height max. 500 px), and make sure that all labels are readable. All text (besides labels) should be removed from the synopsis image.
Please resubmit your revised manuscript online **within one month** and ideally as soon as possible. If we do not receive the revised manuscript within this time period, the file might be closed and any subsequent resubmission would be treated as a new manuscript. Please use the Manuscript Number (above) in all correspondence.
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